NBER WORKING PAPER SERIES THE GROWTH EFFECT OF DEMOCRACY: IS IT HETEROGENOUS AND HOW CAN IT BE ESTIMATED? Torsten Persson Guido Tabellini Working Paper 13150 http://www.nber.org/papers/w13150 NATIONAL BUREAU OF ECONOMIC RESEARCH 1050 Massachusetts Avenue Cambridge, MA 02138 June 2007 We thank participants in a seminar at CIFAR, and especially Dan Trefler, for helpful comments. Financial support from the Swedish Research Council, the Tore Browaldh Foundation, Bocconi University, and CIFAR is gratefully acknowledged. The views expressed herein are those of the author(s) and do not necessarily reflect the views of the National Bureau of Economic Research. 2007 by Torsten Persson and Guido Tabellini. All rights reserved. Short sections of text, not to exceed two paragraphs, may be quoted without explicit permission provided that full credit, including notice, is given to the source.
The Growth Effect of Democracy: Is It Heterogenous and How Can It Be Estimated? Torsten Persson and Guido Tabellini NBER Working Paper No. 13150 June 2007 JEL No. H11,O11 ABSTRACT We estimate the effect of political regime transitions on growth with semi-parametric methods, combining difference in differences with matching, that have not been used in macroeconomic settings. Our semi-parametric estimates suggest that previous parametric estimates may have seriously underestimated the growth effects of democracy. In particular, we find an average negative effect on growth of leaving democracy on the order of -2 percentage points implying effects on income per capita as large as 45 percent over the 1960-2000 panel. Heterogenous characteristics of reforming and non-reforming countries appear to play an important role in driving these results. Torsten Persson Director Institute for International Economic Studies Stockholm University S-106 91 Stockholm SWEDEN and NBER Torsten.Persson@iies.su.se Guido Tabellini IGIER - Universita Bocconi Via Salasco 5 20136 Milano ITALY guido.tabellini@unibocconi.it
1 Introduction Political regimes can change suddenly, because of coups, popular revolts, or the death of leaders. Such changes provide an opportunity to assess whether economic policies or performance are influenced by political institutions. A number of recent papers have exploited this opportunity. Using more or less the same difference-in-difference methodology, they have all estimated the average effects of democratic transitions on economic growth, or some other measures of economic performance, using a post-war panel data set (see e.g., Giavazzi and Tabellini(2005), Papaioannou and Siourounis(2004), Persson(2005), Persson and Tabellini(2006), Rodrik and Wacziarg(2004)). While the difference-in-difference strategy yields interesting results, which are considerably more credible than those from a standard cross-sectional regression,itstillrestsonstrongidentifyingassumptions. 1 Thegoalofthispaperistoreassesstherelationbetweendemocracyand growth, while relaxing some of these strong identifying assumptions. To reach this goal, we re-estimate the average effect of political transitions on economic growth by means of semi-parametric methods. Broadly speaking, we combine aspects of difference-in-difference methods with aspects of propensityscore methods, by giving more weight to the comparisons of reforming and non-reforming countries that have similar probabilities of experiencing democratic reform. Specifically, we first estimate the probability of regime change conditional on a number of observable variables. We then use this estimated probability, the propensity score, to evaluate the difference in growth performance between the countries with and without a regime change. Under the standard assumptions in the propensity-score literature (the selectionon-observables and common-support assumptions), this empirical strategy yields consistent estimates of the average effect of political regime changes, in cases when a standard difference in difference strategy would not. A theoreticalpaperbyabadie(2005)furtherdiscussesthisapproachtoestimation. 2 1 Itishardtofindgoodinstrumentsforregimechanges. JonesandOlken(2005,2006) imaginatively use unexpected deaths of leaders, and the contrast between successful and unsuccessful assassination attempts on leaders, respectively. The latter approach allows them to estimate the likelihood of a democratic transition, but it is likely to generate too weak an instrument(too few successful assassinations and too imprecise timing) for democracy. 2 Athey and Imbens (2006) generalize the difference in difference methodology along related but different lines. Their non-parametric approach also allows for hetereogeneous treatment effects, but relies on estimating the entire distribution of counterfactual out- 2
Heckman et al. (1997) evaluate similar non-experimental estimators, using data from a large-scale US social experiment with job training. Blundell et al. (2004) apply a combination of matching and difference in differences when estimating the effect of UK job training programs. To our knowledge, the present paper is the first to apply matching cum difference-in-difference methodsinamacroeconomiccontext. 3 Themacrosettingraisesspecificissues that are not present is standard microeconomic applications, such as a relatively small sample and different treatment (reform) dates for different observations. Our empirical findings suggest that empirically relevant heterogeneities are indeed present across countries, meaning that the flexibility allowed by semi-paramatric methods is important. We show that transitions from autocracy to democracy are associated with an average growth acceleration of about 1 percentage point, producing a gain in per capita income of about 13percentbytheendofthesampleperiod. This1percentgrowtheffectis imprecisely estimated, but larger than most of the estimates in the literature using straight difference-in-difference methods(see the references mentioned above). The effect of transitions in the opposite direction is even larger: a relapse from democracy to autocracy slows down growth by almost 2 percentage points on average, which implies an income fall of about 45 percent attheendofthesample. Theseeffectsaremuchlargerthanthosecommonly found in the literature. The paper proceeds to discuss the main econometric issues(section 2), describe the data (Section 3), and provide a benchmark with the straight difference-in-difference approach(section 4). We then discuss some preliminaries in the matching procedure(section 5), present the paper s main results on how democracy affects growth(section 6), and conclude(section 7). 2 Econometric Methods This section introduces a number of econometric issues and methods to deal with them. Most of it can probably be skimmed through by econometrically proficient readers who are familiar with the methods used in the treatment comes for the treatment group in the absence of treatment. 3 PerssonandTabellini(2003)applypropensity-scoremethodstoevaluatetheeffectof alternative constitutional features, but they compare a cross section of countries and do not exploit temporal variation in the data 3
literature. Ourgoalistoestimatetheaveragecausaleffectofbecomingademocracy on economic growth. To simplify the argument, we assume throughout the section that we have access to a sample consisting of data from only two types of countries: treated countries that experience a single transition from autocracy into democracy, and control countries that remain autocracies throughoutthesampleperiod. 4 Foreachcountryinthissample,weobserve economicgrowthincountryiandyeart,y i,t,adummyvariableequaltoone underdemocracy,d i,t,andavectorofcovariates,x i,t. 2.1 Difference in difference estimates Several recent papers(see the Introduction) have estimated the average effect of democracy on growth from a panel regression like: y i,t =φd i,t +ρx i,t +α i +θ t +ε i,t, (1) whereα i andθ t arecountryandyearfixedeffects. Thisspecificationseeksto estimate the parameter φ by difference in differences, by comparing average economic growth after the democratic transition minus growth before the transition in the treated countries to the change in economic growth in the control countries over the same period. This estimation method allows for any correlation between the democracy dummy D i,t and time-invariant country features e.g., that fast-growing countries are more likely to become democratic than slow-growing ones since the growth effects of these country features are all captured by the country fixed effect, α i. Nevertheless, identification rests on an important assumption: the selection of countries into democracy have to be uncorrelated withthecountry-specificandtime-varying shocktogrowth,ε i,t. This in turn corresponds to two restrictive assumptions. First, absent any regime change, average growth in treated countries should(counterfactually)havebeenthesameasincontrolcountries(conditionalonx i,t ). This would fail, e.g., if democratic transitions are enacted by far-sighted leaders, whohavealastingimpactongrowthirrespectiveoftheregimechange,orif 4 For the time being, we thus neglect transitions from democracy to autocracy, and exclude from the sample countries that always remained democracies. We also neglect multiple transitions, and only consider countries that had a single transition from autocracy into democracy. These complications are all dealt with in later sections. 4
political transitions coincide with other events such as the economic transitions towards free markets in former socialist countries that may have a lasting impact on economic growth. To make this assumption more credible, the existing literature typically attempts to increase the similarity between treated and controls by including inthevectorx i,t severalcovariates,suchasinitialpercapitaincome,indicators for war years or socialist transitions, indicator variables for continental location(africa, Asia and Latin America) interacted with year dummy variables,andsoon. The second restrictive assumption is that heterogeneity in the effects of democracy should not be systematically related to the occurrence of democracy itself. Circumstances of regime changes differ widely across time and space, as do the types of political institutions adopted or abandoned. Thus, the effects of a crude democracy indicator are likely to differ across observations. If we neglect this heterogeneity and estimate the average effect of democracyasin(1),theunexplainedcomponentofgrowth,ε i,t,alsoincludes theterm(φ i,t φ)d i,t,whereφ i,t isthecountry-specificeffectofdemocracy incountryiandyeart.identificationofφnowrequiresheterogeneityinthe effect of reforms to be uncorrelated with their occurrence. This assumption fails, e.g., if countries self-select into democracy based on the growth effect ofregimechanges(e.g.,d i,t =1morelikelywhenφ i,t >φ). To cope with this assumption, the dummy variable for democratic transitions is sometimes interacted with other observable features of democratic transitions(such as the nature of democratic institutions that are acquired, or the sequence of economic and political reforms). But this strategy quickly runs into the curse of dimensionality problem. The possible interactions and covariates are simply too many, relative to the limited number of democratic transitions. 2.2 Matching estimates based on the propensity score To circumvent the curse of dimensionality, the recent microeconometric literature has often come to rely on semi-parametric methods based on the propensity score. Typically these applications concern a cross section of individuals. But a few recent papers have combined difference-in-difference estimates with matching based on the propensity score, exploiting repeated observations for the same individuals. Abadie(2005) discusses an estimation strategy that uses the propensity score to carry out estimates in the spirit 5
of difference in differences, while Heckman et al. (1997) and Blundell et al. (2004) provide theory as well as microeconometric applications. Thegeneralideaisveryintuitive. Performance growth, inourcase before and after the treatment date is observed for the treated group and the control group. Conventional difference in differences compare the average change in performance for all the treated with the average change in performance for all the controls, on the two sides of a common treatment date. The matching approach instead compares each treated individual with a set of similar controls, and a difference-in-difference estimate is computed with reference only to the matched controls. This way, controls similartothetreatedaregivenlargeweight,andcontrolsverydissimilartoany treated observation may even be deemed entirely non-comparable, i.e., they are left unmatched and given zero weight. Similarity is measured by the onedimensional metric of the propensity score, i.e., the probability of receiving treatment conditional on a set of covariates. Basically, the effect of treatment is estimated by comparing groups of individuals with similar distributions of those covariates that enter the estimation of the propensity score. The microeconometric papers mentioned above discuss the econometric theory behind this methodology, and we refer the reader to these papers for more details. In this section, we confine ourselves to stating and explaining the main identifying assumptions. For this purpose, we need some notation adapted from Persson and Tabellini(2003) and Abadie(2005). 2.2.1 The parameter of interest Asabove,letDbeanindicatorfordemocracy(D=1)orautocracy(D=0). Time is indexed by k, which corresponds to(an average over) years before (k=0)andafter(k=1)theyearofdemocratictransition. LetYi,k D denote potentialgrowthofcountryiinperiodkanddemocraticstated(weusethe symbol Y, in distinction from y in the previous subsection, since growth in periodkisnowanaverageofyearlygrowthratesduringk). Theindividual treatmenteffectofdemocracyincountryiandperiodk isthenyi,k 1 Y0 i,k, theeffectongrowthinperiod1ifthiscountryswitchedfromautocracyto democracy. Consider a subset of the treated countries (i.e., countries with D i,1 = 1) with similar (time-invariant) characteristics, X i. The expected effect of democracy on growth in each of these countries is: α(x i )=E(Y 1 i,1 Y0 i,1 X i,d i,1 =1),. 6
where the expectations operator E refers to unobserved determinants of growth in democracy. Our parameter of interest is the average effect of treatment on the treated, namely: α=eα(x i )=E { E(Y 1 i,1 Y 0 i,1 X i, D i,1 =1) }, (2) where the outer expectations operator E is taken over X in the part of the sample treated with democracy. This parameter measures the effect of democracy on growth in the countries that actually experienced the transition, relative to what would have happened had they remained autocracies. In other words, the relevant counterfactual is remaining under autocracy. Without additional assumptions, the parameter α does not say anything about what growth would have been if the countries that remained autocracies had instead become democracy(this would be a statement about the effect of treatment on the non-treated). The fundamental problem of causal inference is that potential growth in the counterfactual regime is not observed. We only observe actual growth in oneofthetwopossiblepoliticalregimes. Inparticular,inperiod1weonly observeyi,1 1 inthecountriesthatactuallybecamedemocratic(thetreated) andyi,1 0 in the countries that actually had no transition(the controls). But the termyi,1 0 (counterfactual growth in a democracy if it had remained an autocracy) on the right-hand side of(2) is not observed. 2.2.2 Selection on observables To come up with an observable counterpart to Y 0 i,1, we can make the key identifying assumption(cf. Abadie, 2005): E(Y 0 i,1 Y 0 i,0 X i, D i,1 =1)=E(Y 0 i,1 Y 0 i,0 X i, D i,1 =0). (3) The right- handsideof (3)is the(observed)averagechangein growthbetween periods 1 and 0 in countries that remained autocracies throughout (the control group). The left-hand side is the(unobserved) average change in growth that the countries which actually became democracies(the treated group) would have experienced had they remained autocratic. Thus, the critical assumption is that, conditional on X, without their democratic transition the treated countries would have followed a growth path parallel to that of the control countries. This is the analog of the selection on observables 7
assumptioninasimplecross-sectionalcontext 5. Decomposing the expectations operators on both sides of (3), all the terms are observable exceptforone: E(Yi,1 0 X i,, D i,1 =1). Thus, assumption (3) enables us to obtain an observable counterpart of this unobserved counterfactual, that can be used to estimate the parameter of interest in(2). Intuitively, by conditioning on a large enough set of covariates X, we can replace unobserved period 1 growth under autocracy in the treated countries (theterme(yi,1 X 0 i,,d i,1 =1))withobservedgrowthunderautocracyover thesameperiod(theterme(yi,1 0 X i,d i,1 =0))inthosecontrolcountries thathavesimilarcovariatesx i. Importantly, this argument does not impose any functional-form assumption on how democracy impacts on growth. Because the relevant conditional expectations in (3) can all be computed non-parametrically, we can estimate our the parameter of interest, α, non-parametrically just by comparing (weighted) mean outcomes. This is the central difference between matching and linear regression. Matching allows us to draw inferences from local comparisonsonly: aswecomparecountrieswithsimilarvaluesofx,wedonot rely on counterfactuals very different from the observed factuals. However, this desirable property requires that any unobserved heterogeneity in the response of growth to democracy be non-systematic across the two groups of countries. 2.2.3 Propensity score and common support In practice, however, the dimension of X is too large for direct matching to be viable. This is where the propensity score methodology is helpful. An important result due to Rosenbaum and Rubin(1983) implies that comparing countries with the same probability of democratic transition(treatment) given the controls X, is equivalent to comparing countries with similar values of X. Specifically, let p i =p(x i )= Prob[D i,1 =1 X i ] be the conditional probability that country i has a democratic transition duringoursampleperiod,giventhevectorofcontrols,x i.thisconditional 5 AsAbadie(2005)notes,equation(3)coincideswiththesocalledselectiononobservables assumption used in cross sectional studies if in addition we also have E(Yi0 0 X i, D i1 =1)=E(Yi1 0 X i,d i1 =0). 8
probability is also called the propensity score. Assume that the propensity scoreisboundedawayfrom0and1forallcountries,anassumptionknown as the so-called common-support condition: 0<p(X i )<1, all X i. (4) Rosenbaum and Rubin(1983) show that, in a cross sectional setting, conditioningonthevectorxisequivalenttoconditioningonthescalarp.if(4) is satisfied in our two-period context,(3) implies: E(Y 0 i,1 Y 0 i,0 p(x i ), D i,1 =1)=E(Y 0 i,1 Y 0 i,0 p(x i ), D i,1 =0), (5) For countries with similar propensity scores, realized transitions to democracy are random and uncorrelated with growth. We can thus replace the unobserved counterfactual on the left-hand side of (5) with the observed factual on the right-hand side of(5). 2.2.4 Whatdowegain? The main advantage of this semi-parametric (semi-parametric because we have to estimate the propensity score) approach over the parametric differencein-difference approach is that it relaxes linearity. We can thus allow for any heterogeneityin the effectof democracy, as long as it is related tothe observable covariates X. Suppose e.g., that richer countries are more likely to become democracies, and that democracy also works better in richer countries. Then the linear estimates corresponding to equation (1) would be biased unless we also included an interaction term between income and the democracy dummy. This bias is removed if income is included among the covariates X used to estimate the propensity score. Of course, unobserved heterogeneity remains a problem. Any omitted variable uncorrelated with X that influences both the adoption and the effects of democracy would violate selection on observables. But since as a practical matter economic, social and cultural characteristics tend to cluster a great deal across countries, unobserved differences among countries may well correlate with observed differences. A second advantage of this approach is that it allows a simple diagnostic to check that the distribution of observed covariates is balanced between the countries in the treated group and the control group. If the distribution of aspecificcovariateisveryunbalancedinthetwosamplesofcountries,itis 9
important to check if the results are robust to including this variable when estimating the propensity score. Intuitively, if the treated and controls have similar covariates the linearity assumption entailed in conventional difference in difference is just a convenient local approximation. If they do not, the dissimilarity may bias the results. Of course, there is no free lunch. The main cost of a semi-parametric approach is that the estimates are less efficient than parametric estimates (under the null of the assumed functional form). Given the small samples in macroeconomics relative to standard micro applications, the loss in precision is non-neglible. 2.2.5 Implementation in practice Our actual sample unlike the stylized example and typical microeconomic applicationsliketrainingprograms hasdifferenttransitiondatest i,fordifferent observations i = 1,..., I. Of course, our estimation procedure will have to cope with this additional complication. Also different from the example in this section, the actual sample includes transitions from democracy to autocracy. This presents no conceptual problems(see further below), however, so we can continue to think about treatment as a transition into democracy. In practice, we implement the estimation in five steps. (i)webeginbydefiningagroupoftreatedandagroupofcontrolcountries and estimate the probability of treatment. This is done in a cross section by means of a logit regression, where the dependent variable equals one for all countries making a transition at some time within the sample and zero for those that don t, and where all the covariates are time invariant. The estimated probability of a transition to democracy is our measure of the propensity score. (ii) Next, for each country treated with democracy, we compute average growth before and after the date of transition, T i. The difference between thesetwoaveragedgrowthratesisdenotedbyg i. Thus,wemeasure g i = 1 N a i t>t i y i,t 1 N b i t<t i y i,t, (6) wherey i,t is theyearlygrowthin period t andn b i andn a i are thenumber of years before and after and the transition date in country i. (The next section describes how we deal with multiple transitions, so for now think 10
abouttheprocedureasapplyingtoasetupwhereeachcountryhasatmost one transition in the sample period.) (iii) Subsequently, we match each treated country with some of the controls. For each of these controls, we compute the difference in average growth over the periods before and after the transition date in the treated country they are matched with: the expression is thus identical to(6), except that y i,t isreplacedwithy j,t. Wedenotetheresultingvariableasg j i wherethej superscriptreferstoacertaincountryj amongthecontrolsandirefersto thetreatedcountry. Indoingthis,wemakesurethattheyearsoverwhich g i andg j i arecomputedexactlycoincide. (iv) For each treated country, we then compute the weighted average of thenon-parametricdifference-in-differenceestimator ˆα i : ˆα i =g i j w i,j g j i, (7) where w i,j 0, j w i,j = 1, are weights based on the propensity score. These weights differ depending on the detailed properties of the matching estimators and some controls may receive zero weight if they are very different fromthe treatedcountrywithwhichtheyare matched. The parameter ˆα i isourestimateoftheeffectofdemocratictransitionongrowthincountryi. Intuitively, it measures how growth in country i changed after the transition, relative to a weighted average of the(similar) controls it is matched with. (v) Finally, we compute the average estimated effect of transitions to democracyinthe group of treated countries, ˆα, as a simple average of the individual ˆα i estimates,namely: ˆα= 1 ˆα i (8) I wherei denotesthenumberoftreatedcountriesinoursample. Thisisour estimator of the average effect of democracy on growth(the average effect of treatment on the treated). Clearly, this procedure may use each control country several times, as the same controls may be matched with several treated countries and possibly at different dates. This matters for the computation of the standard error of our estimators, since it may introduce correlation between g j i and g j k i.e., between growth in control country j when it is used as a control for treated countries i and k. Of course, the correlation will be positive and 11 i
higher the closer are the transition dates of i and k, while the correlation betweeng j i andgj k mightevenbenegativeifthetransitiondatesarefarpart. The appendix provides analytic expressions for the standard error of α under twoalternativeassumptions: (a)thevariablesg j i andgj k areindependent,(b) the variables g j i and g j k are perfectly correlated. While (b) certainlyyields anupperbound,thetruestandarderrorsmightbelowerthanunder(a)if negative correlation between g j i and g j k is prevalent. When computing the standard errors, we assume that all treated countries have the same variance, asdoallcontrolcountries. Wealsoneglectthattheweightsareestimatedin a first step(i.e., we treat the propensity score as known). Both assumptions arestandardintheappliedliterature(see,e.g.,lechner,2000). 6 3 Data and Sample Definitions Our panel data set includes annual data on economic growth and political regimes for as many countries as possible over the years 1960-2000. Economic growth is measured as the yearly growth rate of per-capita income, and the sourceisthepennworldtables. Weclassifyacountryasdemocraticifthe polity2 variable in the Polity IV data set is strictly positive. The threshold of 0 for polity2 corresponds to a generous definition of democracy, but has the advantage that many large changes in the polity2 are clustered around 0. This is important, since we want to identify the causal effect of regime transitions on growth exploiting the time variation in the data. A definition of democracy based on a higher threshold for polity2 would classify as democratic transitions also very gradual changes in the underlying indicators of polity2, that are unlikely to be associated with significant changes in political regimes. 7 We also include some other covariates, that will be introduced and defined in context. The resulting panel is unbalanced, partly because of data availability and partly because countries do not enter the data set until their year of independence. 6 An alternative tobe pursued in future work would be to compute the standard errors by bootstrapping. Doing so would take into account that the weights w i,j are uncertain, since they are based on(logit) estimates of the propensity score. 7 An alternative would be to use a classification of political regimes, based on a finer subdivisionofthe21-stepscaleforthepolity2 score. Thiswouldturntheanalysisinto the domain off multiple tretments(see e.g., Lechner, 2001) 12
From this panel data set we construct two partly overlapping samples, which are used to study transitions to democracy and autocracy, respectively. When studying transitions into democracy, we include as control countries those that remain autocracies throughout the sample period, while the treated countries are those that experience at least one transition from autocracy to democracy. We call this sample the democratic transitions sample. When studying transitions into autocracy, the control countries remain democracies throughout, while the treated countries have at least one transition from democracy to autocracy. This is called the autocratic transitions sample. Inselectingthesetwosamples,wehadtodealwithanumberofcomplications. A few countries experience transitions close to the beginning or the end of the period for which growth data are available. Since we expect it to take some time for transitions to influence growth, we discard the transitionsthattakeplaceinthelastthreeyearsoftheavailablesample. Wealso discardreformsinthefirstthreeyearsofthepaneltoavoidapoorestimate of growth before the transition. Specifically, we set to missing the observations of growth after(or before) a transition, if the transition is not followed (or preceded) by at least three years of growth data. The country is then considered a control, as if the transition did not occur. In a few countries, especially in Africa and Latin America, we observe transitions that only last for a few years. We discard those lasting(strictly) less than four years, to avoid hinging the estimation on very short growth episodes. Asinthebeginningorendofsampletransitions,wesetgrowthto missing during the years of these short transitions, and classify the country asifthetransitiondidnotoccur. Inanotherfewcountries,weobservemorethanonelongspellofdemocracy or autocracy. Chile, for instance, starts out as a democracy in 1960, it becomes an autocracy (the Pinochet regime) in 1973, and it returns to democracyin1989. ThismeansthatChileisatreatedcountrybothwhen treatment is defined as transition to democracy, and when treatment is defined as transition to autocracy. Therefore, Chile is included as treated in the democratic transitions sample for the years from 1973(when it first becomes anautocracy)untiltheendofthesample. Itisalsoincludedastreatedinautocratic transitions sample from 1960 until 1988(the last year of autocracy). We apply similar sample selection rules to other countries that experience morethanonespellinthesameregimelastingmorethanthreeyears. When transitions are defined in this way, most countries have no more 13
than a single transition in one or both directions. Guatemala, Uganda and Nigeria, however, have two transitions in the same direction. We deal with the transitions in these three countries in two different ways: they are either excluded because the propensity score is outside of the common support range (see below), or included with the transitions in the same direction assumed independent(as if each transition applied to a different treated country). 4 Difference-in-Difference Estimates To provide a benchmark, Table 1 presents results from traditional differencein-difference estimation with yearly data. These results correspond to estimates of equation (1) in various samples. Besides country and year fixed effects,thecovariatesx i,t,includeper-capitaincomelaggedonce,yearfixed effects interacted with indicators for Latin America and for Africa, indicators for war years and lagged war years, and an indicator for formerly socialist countries in Central and Eastern Europe and the Asian provinces of the former Soviet Union after 1989. This specification is similar to those in the existing literature(e.g., Giavazzi and Tabellini 2005, or Persson and Tabellini 2006). Column1imposestheassumptionthattheeffectongrowthofatransition into democracyis the same as the negative of the effect on growth of as transition into autocracy. The effect of democracy is thus estimated in thefullsample. Asintheearlierpapersabove,wefindthattheeffectofdemocratic transitions is positive, inducing a growth acceleration of about 0.5 percentage points. Although not statistically significant, the point estimate isnotatrivialeffectfromaneconomicpointofview. Thelong-runeffectis dampened by the relatively high estimated convergence rate, however. With a convergence rate of 5.5 percent per year, a growth acceleration of about 0.5 percentage points implies a long-run positive effect of democracy on the 14
levelofpercapitaincomeofalmost10percent. 8 The remainder of Table 1 does not impose the symmetry constraint, but estimates the effect of democracy separately from transitions to democracy (columns 2 and 3) and transitions to autocracy(columns 4 and 5), allowing these two effects to differ. Note that when estimating the effect of autocratic transitions in columns 4 and 5, we still display the effect of being a democracy, computed as the negative growth effect of transitions away from democracy. Incolumn2,weletthesampleincludeonlythecountriesthatbecamedemocraciesplusthecountriesthatremainedautocraciesthroughout. 9 In column 3, we add to the sample those countries that remained democratic throughout. Analogously, the sample behind column 4 includes the countries that became autocracies and the more restricted set of countries that remained democratic throughout, while the sample behind column 5 includes both permanent democracies and autocracies. All the estimates in Table 1 convey a similar message: democracy induces a positive, but small and generally insignificant, growth acceleration. The positive effect of transitions to democracy appears larger in absolute value(and in one case statistically significant) than the negative effect of transitions to autocracy. 5 Matching preliminaries Wenowturntothemaincontributionofthepaper,namelythematchingapproach to estimating the growth effects of democracy. Before getting to the actual estimates, however, we need to go through a number of preliminary 8 ThecoefficientφonthedemocracyindicatorDmeasurestheimpacteffectongrowth y t y t 1. Becauselagged(log)incomey t 1 enterontherhsoftheestimatedequation withcoefficientβ,thelong-runeffectonincomecanbecomputedas dy dd = φ β. Withestimates φ=0.5and β = 0.055,weobtainalong-runincomegainof0.09. i.e., about 9 percent. Since the convergence rate β is likely overestimated in yearly data(due to cyclical fluctuations in income), this is almost surely an underestimate of the long-run income gain. 9 This is, of course, the "democratic transition" sample defned in Section 3. In this section, we avoid the term control countries, however, since in a difference in difference estimation with different treatment dates, all countries that do not have a reform in period teffectivelyserveascontrolsforthosecountriethatdohaveareformint. 15
steps including some diagnostics. This section is devoted to these preliminaries. 5.1 Estimating the propensity score As explained in Section 2, the first step to implement a matching cum difference-in-difference estimator is to estimate the propensity score, the probability of treatment, in a cross section of countries (i.e., ignoring the time dimension). We do this separately for the events of becoming a democracyandbecominganautocracy,becausewewanttoallowtheeffectofthe covariates on the probability of transition to be different for the two events. In the democratic transitions sample, the dependent variable is thus zero for the countries that remained autocracies, and one for the countries that experienced at least one transition towards democracy. In the autocratic transitions sample, the dependent variable is zero for the countries that remained democracies throughout, and one for the countries that experienced at least one transition towards autocracy. Thus, the samples are partly overlapping(because some countries like Chile appear in both samples). We estimate the propensity score with a logit regression. The selection of the covariates to enter this regression is a crucial decision, that trades off two opposite concerns. On the one hand, the selection on observables assumption would suggest to include many covariates to ensure that the propensity score is indeed a balancing function. On the other hand, we don t want to predict treatment too well, so as not to violate the common-support assumption. Here is an instance, where the macroeconomic setting bites. Most microeconomic application concentrate on the first concern, because thesampleislargeenoughthatevenrareevents likeanactualtransitionfor anobservationwithalowpropensityscore wouldstilloccurinlargeenough numbers to allow meaningful comparisons(and small standard errors). But in ourcontextwealsohaveto worryaboutnotexcludingtoomanycountries whose state is predicted too well. Thus, we include a limited number of variables that are likely to influence both the occurrence of regime transitions anditseconomiceffects, andwechecktherobustnessoftheresultstotwo alternative specifications. The set of covariates is the same in the democratic and autocratic transitions samples. To capture differences in economic development, we include real per capita income at the beginning of the sample. As explained above, different countries enter our samples at different dates, depending on political history 16
or data availability. To increase comparability, we measure each country s per capita income in the first year it enters a given sample relative to US per capita income in the same year. We call the resulting variable income relative to the US. The countries in these samples have very different political histories. Someofthemhavealonghistorywithentryintodemocracyinthedistant past, or a prolonged autocratic spell. Others became independent some time during the sample period or few years before. To mitigate this important source of heterogeneity, we condition on what Persson and Tabellini(2006b) call domestic democratic capital, which measures the incidence of democracy ineachcountrysince1800(orsincetheyearofindependence,iflater). This variable is assumed to accumulate in years of democracy, but to depreciate under autocracy. The depreciation rate is estimated by Persson and Tabellini (2006b)tofitthehazardratesinatimeseriesregressionwherethedependent variable is exit from democracy and from autocracy. This variable is re-scaledtoliebetween0and1,wherea1correspondstothesteadystate value of a country never exiting from democracy. In this paper, we measure domestic democratic capital in the first year when a country enters the sample. Transitions to democracy or autocracy often occur in waves that include several neighboring countries. To capture this phenomenon, we include a variable measuring the geography of democracy around 1993(the first year in our sample, when we have data for all formerly socialist countries in Central and Eastern Europe). This variable, called foreign democratic capital, is a slight variation on a similar measure used in Persson and Tabellini(2006b). Foreachcountry,itisdefinedastheincidenceofdemocracyin1993among allothercountrieswithina1750kmradius(theradiusreferstothedistance between the capitals). By the definition of a share, this variable too lies between 0 and 1, where a 1 captures the case where all countries in the neighborhood are democratic. Since the sample period varies in length across countries, and since the probabilityofaregimetransitionishigherthelongeristhedurationofthe relevant time period, we also control for the length of the period during which we have available data for each country, a variable called length of sample. This variable is introduced to eliminate the possibility that sample length covaries systematically with growth performance. Wars are often destabilizing for political regimes and, of course, they also hurt economic activity. Thus, we include as a covariate the fraction of war 17
years(including both inter-state and civil wars) over the total period length for which growth data are available, a variable called war years. Finally, regime transitions are more likely for countries that start out with avalueofourdemocracyindex,polity2,closertothethresholdofzero. Atthe sametime,ahighinitialvalueofpolity2 mighthaveanindependenteffecton the economic consequences of regime changes(for instance because a regime change might correspond to a more gradual transition). For this reason, we alsoconsiderincludingthevalueofpolity2 inthefirstyearacountryenters the sample. As we shall see, however, the inclusion of this variable increases a great deal the predictive power of the logit regressions in the sample of autocratic transitions. This, in turn, leads to a much smaller set of treated countries that safely meet the common support condition. Hence, we discuss results with and without the initial value of polity 2. The results of the logit regressions are displayed in Table 2. Columns 1 and 2 refer to the democratic transitions sample, with and without the inclusion of the initial value of polity2. Domestic democratic capital considerably raises the probability of a transition towards democracy, as expected. Foreign democratic capital has a similar positive effect, but this effect is not statistically significant. The frequency of wars discourages democratic transitions, an effect that is statistically significant. Income relative to the US hasnoeffect. Finally,theinclusionoftheinitial valueofpolity2 makesno difference. OverallthepseudoR 2 (theimprovementinthelikelihoodassociatedwiththeinclusionofthecovariatesinadditiontoaconstant)is0.17, suggesting that these covariates leave a lot of residual variation unexplained. Columns 3 and 4 refer to the autocratic transitions sample, with and without the initial value polity2. Here income relative to the US has strong predictive power, with richer countries less likely to relapse into autocracy, asexpected. 10 Foreigndemocraticcapital alsohelpstopredicttransitionsto autocracy, although here the sign is opposite of what one would expect. As anticipated, the inclusion of the initial value of polity2 makes a big difference: the variable is highly significant and with the expected sign, and when itisincludedthepseudor 2 jumpsfrom0.43to0.61. Overall,thesecovariates help to predict transitions from democracy to autocracy much better than transitions in the opposite direction. As already discussed, this is a 10 Theresultsonincomeareconsistentwiththeresultsintheannualhazardratesestimated by Persson and Tabellini(2006b), who find that income does not explain transitions out of autocracy, but does slow down transitions out of democracy. 18
mixed blessing, since it makes the selection on observables assumption more credible, but at the same time strains the credibility of the common support assumption. Figure 1 depicts the density of the estimated propensity score from columns 1and3respectivelyofTable2(i.e.,thespecificationthatdoesnotinclude the initial value of polity2), for both treated and control countries. Observations outside of the common support we impose are dropped and not displayed in Figure 1 (see the discussion in the next subsection). As one would expect from the estimation results, the distribution of the propensity scores for the treated and the controls are more similar in the sample of democratic transitions, where treatment is predicted less well, than in the sample of autocratic transitions. Both samples display considerable overlap between treated and control countries, however. Overall, the figure suggests that matching should work well, at least if the local comparisons are made within relatively broad regions of the propensity score (a coarse balancing function), so as to guarantee overlap. 5.2 Countries inside the common support ThefirstcolumnofTables3aand3breportthefulllistofcountriesineach of the two samples. These are sorted in ascending order of the estimated propensity scores, which are displayed in the third column. To facilitate reading the table, the name of treated countries are indicated by boldface font, whereas the name of control countries are not. The same information is givenincolumn2: thevariabletreated inthesecondcolumnequals0forthe countriesinthecontrolgroupand1forthecountriesinthetreatedgroup. Thelasttwocolumnsofeachtablereportthechangeinpolity2 intheyear of the regime transition, and the year of that(those) transition(s). It is important to verify that the common-support assumption is not obviously violated, and possibly to drop observations for which the estimated propensityscoreistooclosetoitsboundsof 0and1. Considerthedemocratic transitions sample in Table 3a. At the lower bound (the top of the table), we are comfortably away from 0. The first observation, Yemen, is a control with an estimated propensity score of 0.17. The third observation, Iran is the first treated country(according to our generous definition, Iran became a democracy in 1997), with an estimated propensity score of 0.28. At the upper end(the bottom of the table), instead, several treated countries arepredictedverywelltoswitchintodemocracy. Thereisnofirmrulefor 19
how to deal with this situation. We choose to drop all treated observations with a propensity score above 0.9. This has the advantage of not drawing inferences from Guatemala(the unique country to experience two long spells of democracy), and gives a fair margin away from unity. Adopting a higher upper bound and including more countries would not affect the estimates. But the results are sensitive to a more conservative, lower upper bound, essentially because Haiti (with an estimated propensity score of 0.887) is a large outlying observation which makes some difference. We comment more on this below. Next, consider the autocratic transitions sample in Table 3b, where we face the opposite problem. The controls(that remained democracies throughout)arepredictedverywellaround0andthereislittleoverlapwithtreated countries, while at the upper end the lack of overlap is less serious. Here, we choose to drop all observations with an estimated propensity score below0.075andabove0.93. Attheupperendthechoiceismadesothatthe Nigeria and Uganda(the only two treated countries with multiple spells of autocracy) are dropped from the sample. But adopting a higher or lower threshold would not change the results. At the lower end, one outlying observation matters quite a bit for the results: Belarus, which starts out as a (weak) democracy, and drops into dictatorship after a few years. Since thetimeperiodwherewehavedataforbelarusisveryshort,andsincethe next treated country is Greece with a much higher propensity score(0.19 vs. 0.07 for Belarus), we choose to be conservative and exclude Belarus from the commonsupport. Atthelowend,wethusstartthesamplewithAustria,a control with a propensity score slightly above 0.075. Adopting an even more conservative, higher bound for the common support does not affect the final results. 5.3 The balancing property To what extent is the propensity score a balancing function, i.e., how well does our matching on the propensity score balance the distribution of relevant covariates across treated and control countries? The answer to this question is important, because this is where the value added of this methodology lies. Tables4aand4bprovidetheanswerforourtwosamplesofdemocraticand autocratic transitions. Eachdoublerowinthetablereferstoaspecificcovariate. Weconsider all covariates included in the logit regressions of Table 2(including the ini- 20
tial value of polity2), plus three dummy variables for continental location (in Latin America, or Asia, or Africa). The upper single row (labeled unmatched) for each variable displays the simple average of that variable in the treated groups and control group, respectively, plus the tstatistic and thep-valueforthe null hypothesis thattheseaverages arethe same inthe treated and control group. This first set of statistics is calculated over the full set of countries listed in Tables 3a and 3b, respectively, before imposing the common support assumption. Clearly, the null of equal means is rejected formanyvariablesineitherorbothofthetables. Thus,treatedandcontrol countries differ systematically with regard to economic development(relative income), political history(domestic democratic capital), and-political geography(foreign democratic capital). Initial democracy as measured by polity2 is also very different in the treated and control groups in the "autocratic transitions" sample. Finally, the treated and control groups also seem to be drawn from different continents(in particular with regard to Latin America and Africa). The lower single row for each variable(labeled matched) present a similarsetofstatisticscalculatedinadifferentway. First,weimposethecommon support assumption for both the treated and the control countries, as discussed above. We then calculated the means for the treated countries. Clearly, this changes their means for the treated group. Second, we display the matched means for the control countries, namely a weighted average where each control country receives a weight based on the propensity score, corresponding to the matching procedure described in the next subsection (see also equations(7) and(8) above). Clearly, matching equalizes the means of all covariates used in the logit regression. Interestingly, it also reduces the difference in means of some of the other covariates, Africa and Latin America in Table 4b, Latin America in Table 4a. This gives some credence to our earlier expectation that observed(included among the covariates) and unobserved(not included among the covariates) country characteristics may be correlated. In the autocratic transitions sample, however, the variable initial value of polity2 retains a very different distribution in the treated and control groups, which suggests the importance of also conditioning on the initial value of polity2 in this sample. Overall, and with the caveat just mentioned on initial value of polity2, matching seems indispensable to achieve a balanced distribution of covariates between treated and control countries the so-called balancing property. Without matching based on the propensity scores, the two samples are quite 21